Comment on acp-2021-1062

This work explores the dust emission and deposition distributions in East Asia induced by an extremely severe dust storm in spring 2021 using the four-dimensional variational method. The authors used scientifically plausible experimental methods with reasonable observation datasets. Therefore, this manuscript will be acceptable as a paper with minimum quality standards after a major revision of English errata and a minor revision of scientific descriptions. However, the experimental designs and conclusion of this work are not scientifically significant very much. To increase the scientific significance of this work, the authors should carry out additional data-assimilation experiments and reclassify dustsource regions in China/Mongolia. The reclassification of dust-source regions could change the authors’ conclusion. The decision to accept or reject this manuscript as an article of Atmospheric Chemistry and Physics, one of the high-impact journals, is left to the editor.

to keep using the wind field data and advection model that cannot reproduce vertical sheers to inverse dust emissions. This inconsistency is first and foremost a matter of the model dynamics.
Page 16, Lines 10, 29 and 31; Page 18, Lines 6 and 23: it's misleading to refer to domestic sources/emission/deserts as "local" ones. Local means neighborhood or specific. In this study, for instance, the distance from Beijing City in NCP to the Alxa Desert in China is more than 1000 km while it's 550 km to the Sino-Mongolian border. However, the authors refer to Alxa as a local source but Mongolian Gobi as a faraway source. The "local" should be replaced by "domestic".
Page 16, Lines 21-25: the authors found interesting characteristics of dust transport and deposition for each storm period. This study would have been a much better paper if the authors gave a deeper insight into the meteorological causes of the dust transport/deposition characteristics rather than just stating the facts. Each transport/deposition can be probably explained by the dynamics of synoptic meteorological fields.
In addition, I have a question. Did the source apportionment simulations last for only the SD1, SD2, or SD3 period? If so, the simulation periods are only 2 or 3 days. When a dust plume flows directly from the source region to NCP or NWP, the 2 or 3 days is long enough. However, when a dust plume is caught by synoptic disturbances multiple times, it might take more than 3 days for the plume to travel 2000 km from western Mongolia to NCP/NWP. Is it possible that the short simulation time is one of the reasons why the Alxa Desert less influenced NCP/NWP during SD1?
Page 18, Summary and conclusion: Point 1: The authors repeatedly emphasized that the MODIS AODs were screened by Angstrom exponents and bias-corrected by non-dust aerosol simulations. The PM10 data were also bias-corrected. The authors cited the papers of these preprocessing methods, but didn't present the improvements of the inversion for the 2021 dust storms made by these preprocessing methods at all. Even if the preprocessing methods worked well in the case of previous studies, there might be not much positive impact on the inversion of the 2021 dust storms. If the preprocessing methods are emphasized in Abstract and Summary, it should be shown in this manuscript how much the inversion is improved by the preprocesses for the cases of the 2021 dust storms. If not, the preprocessing methods shouldn't be emphasized in Abstract and Summary.
Furthermore, the authors emphasized that both the MODIS AOD and PM10 data were simultaneously assimilated to estimate dust emissions. However, its benefits were not quantitatively presented in this study. I'm very interested in the difference of the inversion results between a MODIS AOD-only assimilation, a PM10-only assimilation, and the simultaneous assimilation. If the difference is shown in the manuscript, it will be an alternative to independent validation with a subset of leaving data. This study would have been a much better paper if the authors presented more than one inversion results illustrating the quantitative improvements made by the preprocessing methods and the simultaneous data assimilation. Point 2: The authors divided the dust source regions into Chinese sources and Mongolian sources in this study. However, it's not a scientific classification because the Sino-Mongolian border in the Gobi Desert was artificially or politically drawn, not geologically or biologically. Although the authors cited Han et al. (2021) for Mongolian desertification, Han et al. (2021) evaluated only Mongolia and didn't compare the Mongolian Gobi and the Chinese Gobi quantitatively. If the classification with the Sino-Mongolian border is a scientific or environmentally crucial issue, it should be clarified first that the desertification in the Mongolian Gobi is much more serious than in the Chinese Gobi, before the source apportionment study.
Furthermore, the authors concluded that "local" Chinese deserts play a small role in the dust deposition over FWP and NCP compared to the contribution of "long" transports from Mongolia. This conclusion is very misleading. The northeastern part of the Gobi Desert, which is located in Mongolia, is much closer to FWP/NCP than the southwestern part of the Gobi Desert, which is located in China. In other words, Chinese deserts are not always "local" for FWP/NCP and Mongolian deserts are not always far away from FWP/NCP. I think it will be more scientifically plausible to classify dust source regions using the distance, latitude, altitude, and vegetation, not using national borders. If the reclassification was performed, this study would be an excellent paper.

Specific comments:
Figures 2-5 and S1-S3: The font of each map's title is too small.
Page 6, Lines 15-16: I don't think the bias-corrected PM10 data CLEARLY shows the shape of the dust storm. It's too subjective to say "clear" for this distribution.
Page 6, Line 17: the authors say "the shape of the simulated dust plume matches well with the observed shape," but I think "it's slightly matched." To use "well" is overvaluation.
Page 8, Line 25: the model has only eight layers from the surface to 10 km, which is very sparse, especially in the PBL, to investigate aerosol emission and deposition. Usually, stateof-the-art aerosol dispersion models have more than 50 layers from the surface to the tropopause, including more than 10 layers only in the PBL. Why is the vertical resolution set so low? Even if the meteorological fields are provided from ECMWF, the sparse layers in the dust model will result in a very large vertical numerical diffusion, which deteriorates regional aerosol simulations. May I have the authors' opinion?
Page 12, Eq. 4: there's no explanation for the background error covariance matrix B in the text.